The Case of the Indiscriminate Waveform

PEA Arrest

From the very start of our Residency training, Emergency Medicine Physicians are tasked with committing to memory the correctable causes of PEA arrest. It is expected any intern worth their salt should be able to recite the H’s & T’s proselytized by the AHA as far back as 1995 (1). And yet, it quickly becomes evident that this strategy for the management of PEA arrest is not only unwieldy and impractical, but the evidentiary basis supporting its use is minimal. In fact, a brief perusal of the evidence supporting this AHA document reveals that there is none (1).

Recently a more practical strategy was published in Medical Principles and Practice by Littman et al in 2014 (2) suggesting using QRS width to help determine the cause of the arrest. The authors claim that narrow complex rhythms represent a mechanical source of the arrest (hypovolemia, cardiac tamponade, tension pneumothorax, pulmonary embolism, and mechanical hyperinflation), and a wide complex represents a metabolic or left ventricular problem (hyperkalemia, sodium channel blockade, or acute myocardial infarction). And while this algorithm garnered a great deal of popularity in the FOAM community it too is based off very little legitimate evidence. In fact, the authors fail to offer evidence supporting the notion that their strategy accurately predicts etiologies of arrest. The passage reads as follows:

The general assumption is that narrow-complex PEA is generally due to a mechanical problem frequently caused by right ventricular inflow or outflow obstruction, whereas wide-complex PEA is typically due to a metabolic problem or ischemia and left ventricular failure. Wide-complex PEA may also indicate agonal rhythm (2).

The most robust evidentiary support for narrow complex rhythms representing a readily correctable cause of arrest, originates from a single paper published in 1992 in Chest by Paradis et al (3). This paper examines a cohort of 94 patients in PEA arrest. Using arterial catheters, the authors found that a portion of these patients had what they called pseudo-PEA, or a pulse demonstrated on arterial waveform that was not detected through direct palpation. The authors cite that patients with pseudo-PEA were more likely to have a narrow QRS than those in true PEA arrest. And while the mean QRS width was significantly more narrow in patients in pseudo-PEA (0.12 vs 0.24 ms), the corresponding interquartile ranges varied too much (0.04-0.24 vs 0.11-0.56 ms) for this measurement to be used clinically. Furthermore, the authors did not investigate the specific etiologies responsible for patients’ presentations and how they related to QRS width. Although the authors cite that patients with narrow complex waveforms demonstrated significantly improved short-term outcomes and more frequently responded to pressor therapy (23% vs 77.8%) when compared to their wide-complex counterparts (35.9% Vs 14.5%), these differences did not translate into improvements in neurologically intact survival (3).

A recent article published in Resuscitation sought to directly examine the utility of QRS width in predicting the etiology of cardiac arrest (4). Published by Bergum et al, this was a prospective observational cohort examining patients experiencing in-hospital cardiac arrests (IHCA) with an initial rhythm determined to be PEA. The authors then focused on the subset of PEA patients in whom they could establish a definitive cause of their arrest. Using this cohort and the data garnered from the defibrillator waveform analysis during the resuscitation, the authors examined the predictive value of the EKG pattern to predict the underlying cause of the arrest.

Over a 4-year period, the authors identified 144 patients who experienced an IHCA with an initial rhythm of PEA. Of these, 51 patients had a readily identifiable cause of their arrest. EKG criteria were measured independently by two electrophysiologists.  The vast majority (90%, 46/51) of the EKGs analyzed were considered to be a wide-complex (width> 120 ms) and 63% (32/51) were considered bradycardic (<60 bpm). Only 6% (3/51) were considered normal.

In brief no EKG criteria was predictive of either the etiology leading to the arrest or survival to hospital Screen Shot 2016-05-02 at 4.19.43 PMdischarge. Of the 21 patients who achieved ROSC, the HR varied from 25 to 128 BPM and the QRS was anywhere from 79-264 ms. Similar variability was observed in the 6 patients who survived to hospital discharge. Fig 2 and fig 3 in the manuscript clearly illustrate there is no discernible association between QRS width and the etiology of arrest or likelihood of neurologically intact survival.

The limitations of this study are many. Its small sample size makes it difficult to draw any definitive conclusions from these observations. There may very well be an association with QRS Screen Shot 2016-05-02 at 4.22.08 PM
width and cause of arrest that is hidden in statistical noise, but if it does exist this association is weak and erratic. This data should certainly cause us pause when considering the utility of the QRS complex in PEA arrest. Its use should be limited to determining if and when to administer treatments for hyperkalemia.

PEA  is so prognostically dismal because the majority of these arrests are due to an agonal rhythm (5). Caused by either severe cardiac dysfunction or more commonly a ventricular arrhythmia that, because of a prolonged downtime, spontaneously converted or was defibrillated into an agonal rhythm. As such the most reliable predictive utility of PEA in cardiac arrest is as a surrogate for a prolonged downtime. Despite this poor prognosis, a small number of these patients can have a good outcome if a correctable cause can be rapidly identified. The H’s and T’s proposed by the AHA is far too complex, unwieldy and based on little empiric evidence. The alternative strategy of using the QRS width to guide resuscitative efforts, though more straightforward, is based off an assumption that when empirically tested does not reliably predict causes or outcomes. Rather, a far simpler approach should be employed. One that does not focus on every possible cause for PEA arrest no matter how rare or ineffective our treatments are, but focuses on the few causes we can rapidly and effectively correct. These correctable causes are hypoxia, hypovolemia, tension pneumothorax, cardiac tamponade, and pseudo-PEA. Rather than using the EKG, which consistently fails to reliably differentiate these etiologies, the utilization of bedside ultrasound can quickly and accurately identify 4 of the 5 correctable causes while the rapid placement of an ETT will empirically account for the remainder.

The Fog of War, was first coined by Prussian Military Analyst Carl Von Clausewitz to describe the uncertainty in combat.

War is the realm of uncertainty; three quarters of the factors on which action in war is based are wrapped in a fog of greater or lesser uncertainty. A sensitive and discriminating judgment is called for; a skilled intelligence to scent out the truth.

So too is the uncertainty we face when managing patients in cardiac arrest. Rarely are the cause, course and potential solutions conveniently laid out in a clear and concise fashion. We are forced to use clinical surrogates as beacons to assist in navigating this uncertain course.  It behooves us to select clinical tools that are both reliable and accurate. Such is the skilled intelligence to scent out the truth.

Sources Cited:

  1. Kloeck et al. A practical approach to the aetiology of pulseless electrical activity. A simple 10-step training mnemonic. Resuscitation 1995; 30:157–159
  2. Littmann et al. A Simplified and Structured Teaching Tool for the Evaluation and Management of Pulseless Electrical Activity. Med Princ Pract 2014; 23: 1 – 6.
  3. Paradis NA, Martin GB, Goetting MG, Rivers EP, Feingold M, Nowak RM. Aortic pressure during human cardiac arrest. Identification of pseudo-electromechanical dissociation. Chest. 1992;101(1):123-8
  4.  Bergum et al. ECG patterns in early pulseless electrical activity–associations with aetiology and survival of in-hospital cardiac arrest.Published online April 3oth 2016
  5. Desbiens NA. Simplifying the diagnosis and management of pulseless electrical activity in adults: a qualitative review. Critical Care Medicine 2008;36(2):391-6

 

 

 

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The Case of the Man Made of Straw

Analgesia for renal colic

So often when interpreting the medical literature, success is determined by how you define it. Such is the case with a recent article on the management of pain due to ureteral colic. Published in the Lancet in 2016, Pathan et al examined the efficacy of IM diclofenax, IV acetaminophen, or IV morphine in treating the pain related to urolithiasis. The authors randomized 1644 patients presenting to the Emergency Department with renal colic to receive either IM diclofenax, IV acetaminophen, or IV morphine, each with their respective placebos (1).

Patients randomized to both IM diclofenax and IV acetaminophen achieved moderately more pain relief than patients randomized to receive IV morphine. 61% of the patients randomized to receive IV morphine achieved the authors’ primary outcome, a reduction in pain by greater than 50% at 30 minutes. By comparison, 68% and 66% of the respective patients randomized to IM diclofenax and IV acetaminophen experienced the same reduction in pain. This difference became only more apparent when the per-protocol analysis (the patients with radiographically confirmed renal colic) was examined. In this subset, 50% reduction was achieved in 69%, 68% and 60% in the diclofenax, acetaminophen, and morphine groups respectively. Likewise, more patients randomized to either the IM diclofenax or IV acetaminophen groups had a 3-point or greater drop in their pain scores by 30-minutes. In addition, patients in the IV morphine group more frequently required rescue doses of IV morphine.

Essentially both diclofenax and acetaminophen outperformed morphine in every outcome measure assessed. And so are we to believe that for the treatment of renal colic there is a paradoxical shift in the potency of analgesic medications from what has been our global experience? Is there a physiologic explanation for this singularity? I suspect the answer is far simpler, and is far more likely to be found in the trial’s definition of success.

Patients randomized to receive IV morphine, were given a 0.1 mg/kg bolus. And while this dose is commonly used in clinical trials, it does not consistently provide clinically adequate analgesia. A large portion of patients administered 0.1 mg/kg will require additional doses of IV morphine to reach blood levels required to achieve analgesia. In fact, in most cohorts examining the adequate dose of IV morphine, when administered a dose of 0.1 mg/kg, more than 50% of patients will require further dosing to attain analgesic effects. Bijur et al found when using a dose of 0.1 mg/kg of IV morphine in a cohort of patients presenting to the Emergency Department in severe pain, only 35% would have a reduction in their pain scores by 50% by 30 minutes (2). Birbaum et al found that only 44% of patients receiving a dose of 0.1m/kg achieved a 50% reduction in pain at 30 minutes (3).  As such, the 39% of patients requiring additional pain medication observed in the Pathan et al cohort is far from unexpected.

Despite the 0.1 mg/kg dose being commonly utilized, it is an unfair and unrealistic comparison. It is what amounts to a straw man comparator. Allowing for the appearance of sport without truly posing a challenge. To truly obtain fast and adequate analgesia from IV morphine, the dose should be rapidly titrated to effect. In a trial performed by Aubrun et al on post-surgical patients, a protocol of 2-3mg of IV morphine every 5-minutes achieved analgesia in 100% of patients, but the number of doses varied wildly from patient to patient (4). Multiple Emergency Department cohorts have demonstrated that appropriate analgesia is safely and quickly achieved in close to 100% of patients when rapid escalation of opiate pain medication is utilized (5,6). And so what is noted as need for rescue medications in clinical trials, is in reality the appropriate method of achieving adequate analgesia when using IV opiates.

While IM diclofenax and IV acetaminophen may provide superior relief to inadequate doses of IV morphine, this does not translate to appropriate or adequate pain relief for the patient. Although 68% and 66% percent of patients in the diclofenax and acetaminophen groups experienced a 50% reduction in pain at 30 minutes, 32% and 34% did not. 12% and 20% required rescue analgesia. These reductions in pain were achieved at 30-minutes following medication administration. With the appropriately titrated dose of morphine, adequate pain relief can be achieved far earlier. And while this article certainly demonstrates that both NSAIDs and acetaminophen are reasonable options over the course of a patient’s Emergency Department stay, it should not dissuade us from the early and appropriate use of IV opiate analgesics.

Sources Cited:

  1. Pathan, SA, Mitra, B, Straney, LD et al.Delivering safe and effective analgesia for management of renal colic in the emergency department: a double-blind, multigroup, randomised controlled trial.Lancet. 2016
  2. Bijur PE, Kenny MK, Gallagher EJ. Intravenous morphine at 0.1 mg/kg is not effective for controlling severe acute pain in the majority of patients. Ann Emerg Med. 2005;46(4):362-7.
  3. Birnbaum A, Esses D, Bijur PE, Holden L, Gallagher EJ. Randomized double-blind placebo-controlled trial of two intravenous morphine dosages (0.10 mg/kg and 0.15 mg/kg) in emergency department patients with moderate to severe acute pain. Ann Emerg Med. 2007;49(4):445-53, 453.e1-2.
  4. Coghill RC, Eisenach J. Individual differences in pain sensitivity: implications for treatment decisions. Anesthesiology. 2003;98(6):1312-4.
  5. Chang AK, Bijur PE, Campbell CM, et al. Safety and efficacy of rapid titration using 1mg doses of intravenous hydromorphone in emergency department patients with acute severe pain: the “1þ1” protocol. Ann Emerg Med. 2009;54:221-225.
  6. Chang AK, Bijur PE, Holden L, Gallagher EJ. Efficacy of an Acute Pain Titration Protocol Driven by Patient Response to a Simple Query: Do You Want More Pain Medication?. Ann Emerg Med. 2015;

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The Case of the Perfect Imperfection

Ink Blot Test

The Enemy of Good is Perfect

The interpretation of literature is not dissimilar from the interpretation of the Rorschach tests. To one person the data appears to be a freshly hatched butterfly full of hope and promise. While to another it is a discomforting stain resulting from the splatter of improperly handled bodily excrement. What you see when looking at the data is based less on the strength of the trial in question and more on your own intrinsic biases. This psycho-statistical phenomenon has never been more true than with anti-arrhythmic medications in cardiac arrest. Those that believe in their efficacy cling strongly to their potential physiological benefits and data from two small RCTs demonstrating an increase in survival to hospital admission in patients who received amiodarone vs placebo or lidocaine (1,2). Those of us who are bent more towards nihilism discard these findings as surrogate endpoints which do not translate into patient oriented survival. Despite being the largest study examining this question, enrolling over 4,000 patients, I fear that the ALPS trial will do nothing to change these conflicting opinions.

Published in the NEJM on April 4th 2016, Kudenchuck et al examined 3026 patients in refractory ventricular fibrillation or pulseless ventricular tachycardia, randomly assigned to receive either amiodarone, lidocaine or placebo (3). Patients were enrolled if they were found to be in a shockable rhythm which was resistant to at least one attempt at electrical defibrillation and the use of vasoactive agents. Patients were administered either 300 mg of amiodarone, 120  mg of lidocaine, or 3 ml of a saline-based placebo. If further attempts at defibrillation were unsuccessful paramedics were permitted to administer a second bolus at half the dose of the first.

The authors found survival to hospital discharge (their primary endpoint) varied little between groups (24.4%, 23.7% and 21% respectively). This 3.2% and 2.6% absolute difference in survival between the amiodarone vs placebo, and lidocaine vs placebo failed to reach statistical significance (p= 0.08 and 0.16 respectively). The author did note that despite their statistical failure, both amiodarone and lidocaine demonstrated signs of efficacy. Patients randomized to either the amiodarone or lidocaine arms received less defibrillation attempts before achieving ROSC (5, 5, 6 respectively) and survived to hospital admission (45.7%, 47% 39% respectively) more frequently than patient randomized to the placebo arm. In the subset of patients whose arrest was witnessed by bystanders, the authors report a statistically significant increase in patients discharged from the hospital alive in both the amiodarone and lidocaine group when compared to placebo (27.7%, 28.7% and 22.7% respectively) (3).

Some will argue that amiodarone and lidocaine’s benefits were hidden behind a statistically insignificant p-value due in part to a misjudgment in the power calculation. This very well may be true. Certainly patients in both the amiodarone and lidocaine groups seem to respond to the antiarrhythmic effects of the drug therapy. But these upstream benefits did not translate into neurologically intact survival. Survival with good neurological outcome (mRS ≤3) was 18.8%, 17.5% and 16.6% respectively (3). More importantly since their primary endpoint failed to reach statistical significance, it is equally reasonable to argue that these trends towards benefit occurred simply by chance alone. That these small improvements in prehospital outcomes were a measure of a prognostically healthier population rather than an effect of the lidocaine or amiodarone. It is not hard to imagine that patients who survive to hospital admission more frequently and require less shocks are the same patients who are more likely to have improved neurological survival.

But let us suppose for a moment that the trends observed in the ALPS Trial describe a true benefit in the treatment of refractory ventricular fibrillation in OHCA. To what end? The authors primary endpoint was based off a per-protocol analysis of their cohort. As such they excluded a large portion of patients (1,627) because on retrospective analysis their initial rhythms were not ventricular fibrillation or pulseless ventricular tachycardia (3). This led to a highly select population, intended to optimize the trials ability to discern benefit for the treatments in question. But such an analysis comes at a cost of its external validity. Even in this artificial population the authors found only small trends to improvement in survival and had to perform further subgroup analysis to demonstrate statistical benefit. In fact, when the intention to treat population is examined even these trends towards improved survival all but disappear. Patient randomized to the amiodarone, lidocaine, placebo group had survived to hospital discharge at a rate of 19%, 18.4%, and17.6% respectively (3). What this means is for the overwhelming majority of patients in cardiac arrest with a shockable rhythm, amiodarone or lidocaine will provide no benefit.

One could argue that despite the overall minimal effect, these drugs should be administered to all comers on the rare chance they may help one individual patient. And this position seems reasonable when viewed from this single perspective. But when each of these low yield, ineffective therapeutic strategies are stacked one on top of another, on top of another on top of another, the resulting system is unwieldy and ineffective. Cardiac arrest is a high acuity, time dependent disease state. We should focus on delivering a small number of high yield interventions in a timely fashion.  Continued attention on interventions which are unable to demonstrate statistically meaningful improvements in neurological outcomes in over 3,000 patients does nothing but add cognitive clutter to an already chaotic milieu.

This trial design does not account for the unintended consequences of adding extraneous and ineffective complexities to your resuscitation strategy. Trials like the OPALS and the Olasveengen et al cohort which examine the value of ACLS, when added to CPR and rapid defibrillation, demonstrated that such resuscitative intricacies provide no additional survival benefits to patients (4,5).

While the administration of of either amiodarone or lidocaine will likely have little effect on patient outcomes, it is important not to lose sight of the bigger picture. Our current strategy in the management of sudden cardiac arrest is to regain a perfusing rhythm through the application of CPR and rapid defibrillation. Every trial that has ever shown benefit in patient survival focused on the efficient deployment of these two interventions. So often high quality chest compressions, rapid rhythm analysis, avoiding perishock pauses and overzealous ventilatory strategies are overlooked in favor of accommodating the proper order of ACLS medications (6). The false Dichotomy Fallacy is better known by the phrase, the enemy of good is perfect. By creating a system that attempts to account for every last cause of cardiac arrest no matter how unlikely, regardless of the impotency of our resulting treatments, we create a system that is perfect in every way except that it is cumbersome and ineffective. A system that serves only to distract from the select few interventions that truly matter.

Sources Cited:

 

  1. Kudenchuk PJ,Cobb LACopass MK, et al. Amiodarone for resuscitation after out-of-hospital cardiac arrest due to ventricular fibrillation. N Engl J Med 1999;341:871-878
  2. Dorian P,Cass DSchwartz BCooper RGelaznikas RBarr A. Amiodarone as compared with lidocaine for shock-resistant ventricular fibrillation. N Engl J Med 2002;346:884-890
  3. Kudenchuk PJ, Brown SP, Daya M, et al. Amiodarone, lidocaine, or placebo in out-of-hospital cardiac arrest. N Engl J Med. DOI: 1056/NEJMoa1514204
  4. Stiell IG, Wells GA, Field B, et al. Advanced cardiac life support in out-of-hospital cardiac arrest. N Engl J Med. 2004;351(7):647-56.
  5. Olasveengen TM, Sunde K, Brunborg C, Thowsen J, Steen PA, Wik L. Intravenous drug administration during out-of-hospital cardiac arrest: a randomized trial. JAMA. 2009;302(20):2222-9.
  6. Gray R, Iyanaga M, Wang HE. Decreases in basic life support chest compression fraction after advanced life support arrival. Resuscitation. 2012;83(11):e208-9.

 

 

Weren’t they given 120 mg of lidocaine (or 60 mg if they weighed less than 100 lbs)?

 

Any role to add in the stuff about EMS witnessed arrest?

Do you want to mention how the results were inconsistent in the subgroups (if I remember correctly, lido had not benefit in EMS witnessed arrest but amio did which is strange and probably just means that all the subgroup stuff is random)

 

This is the most important thing you say in the entire post. Bold? I know it’s not quite your style but

 

Is it important to point out that continuing to give these meds to all comers may create more ROSC w/ poor neurologic outcomes or is that really beyond scope of this trial and shouldn’t be mentioned?

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A Case of Shadows Part II

Bedside Ultrasound

I think we all can agree that the subtleties of the thoracic cavity go far beyond the diagnostic capabilities of our standard two-view chest x-ray. We have robust data that demonstrates the superb diagnostic prowess of bedside ultrasound (US) when compared to the mediocrity of plain films (1, 2,3,4). And yet more information is not always better. Studies examining diagnostic characteristics of a test cannot predict the downstream effects its use will have on patient care. To uncover such consequences, these diagnostic tools have to be tested in the clinical arena. A recent trial did just that.

Published in Chest in 2016, Jones et al examined the effect bedside US had on the diagnosis and management of pneumonia in a pediatric population presenting to the Emergency Department. The authors randomized 191 well appearing children (< 21 years old) in whom the treating physician was concerned for pneumonia, to either a standard work up using a two-view chest x-ray (CXR) or bedside US. These sonographic studies were performed by Pediatric Emergency attendings or fellows, all of whom underwent a 1-hour training course in lung ultrasonography. Patients randomized to the bedside US group were permitted to receive a CXR if the treating or admitting physician felt it was clinically necessary (5).

The authors found a statistically significant reduction (38%) in their primary endpoint, CXR utilization in the patients randomized to the bedside US group. When authors excluded CXRs that were determined to have been performed for non-clinical reasons (requested by admitting physician, parent, guarding or referring physician), bedside US was found to have the potential of reducing CXR utilization by 67%. The authors claim this reduction produced $9,200 in savings. All this with no events of missed pneumonia during the follow-up period (5).

Given US’s superiority to CXR for the diagnosis of pneumonia, these findings are far from surprising (1,2). I imagine similar results would be obtained if the diagnostic capabilities of plain films were compared to CT scan. This trial does provide insight into how the integration of bedside US in general practice may affect clinical management. The authors observed a significant increase in the rate of pneumonia diagnosed in patients randomized to bedside US when compared to the standard treatment arm (28.2% vs 18.1%). This 10% absolute increase consisted completely of diagnoses made by bedside US. In fact, the number of pneumonias diagnosed by CXR in each group was identical (13.6%). Unsurprisingly, this increase in diagnoses coincided directly with a 10% absolute increase in the rate of antibiotic use (37.9% vs 27.3%) in patients randomized to bedside US (5). And yet despite this increase in diagnostic yield, the authors found no difference in clinical outcomes.

This study underscores the subset of sonographically defined pneumonias, that would otherwise go undiagnosed by CXR. In the past these would have been considered bronchitis or URI of viral etiology and treatment with antibiotics would not have been recommended. Given that the clinical outcomes between the two groups were identical, it is reasonable to assume the majority of these would resolve with symptomatic treatment alone. Certainly without bedside US we have not been stricken with a plague of cryptogenic pneumonias undetectable by plain films. US positive, CXR negative pneumonia is a radiographically defined disease that lacks the clinical mass to support its diagnostic reputation. In short, over-diagnosis.

This is not a statistical lark. It is simply the end result of applying a test with more diagnostic accuracy than the one which was previously employed. Furthermore, it is not the first time we have seen the application of bedside US lead to an increase in downstream testing and treatment. In 2014 Laursen et al published an article in Lancet Respiratory Medicine which examined the use of bedside US to evaluate patients presenting to the Emergency Department with shortness of breath. I have discussed this trial in detail in a previous post, but in brief the authors randomized 320 patients presenting to the Emergency Department with respiratory complaints to either a standard work as per the treating physician or the addition of a bedside sonographic assessment of the cardiovascular, pulmonary and deep venous anatomy. Similar to Jones et al, the authors found more pathology in the group randomized to bedside US. These findings led to increased downstream testing and interventions. Despite these changes in management, patients randomized to the bedside US group had a noticeable trend to worse 30-day mortality (12% vs 7% p= 0.13) (6).

I’m sure to some this will appear as an attack against ultrasound, an argument against its use in the Emergency Department. This is of course not the case. Rather this post should be viewed as an examination of the unintended consequences of replacing the old standard with a new more diagnostically robust alternative. Some may argue that the proper response should be to decipher which sonographic findings require antibiotics and which do not. They may very well be right, but I would argue time and time again we have proven ourselves incapable of making such clinical distinctions and will always rule in favor of action.

A test’s true value is not found in its diagnostic accuracy. It cannot be explained simply through its sensitivity or specificity. Rather a test’s worth lies in how it interacts with the surrounding environment, how its is utilized by the clinical operator. Ultrasound is a powerful tool that has already improved many aspects of patient care in the Emergency Department. But its diagnostic prowess comes at the price of information. Information in the form of radiographic disease whose clinical relevance is not always clear. While such findings do not mean we should abandon this valuable bedside tool, it does remind us that it is a test. And like any test we should be mindful in whom it is applied. We owe it to ourselves and our patients not only to hone our skills in the technical aspects of ultrasonography but to understand the downstream consequences of these new found abilities.

Sources Cited:

  1. Chavez MA, Shams N, Ellington LE, et al. Lung ultrasound for the diagnosis of pneumonia in adults: a systematic review and meta-analysis. Respir Res. 2014;15:50.
  2. Pereda MA, Chavez MA, Hooper-miele CC, et al. Lung ultrasound for the diagnosis of pneumonia in children: a meta-analysis. Pediatrics. 2015;135(4):714-22.
  3. Al Deeb M, Barbic S, Featherstone R, Dankoff J, Barbic D. Point-of-care ultrasonography for the diagnosis of acute cardiogenic pulmonary edema in patients presenting with acute dyspnea: a systematic review and meta-analysis. Acad Emerg Med. 2014;21:(8)843-52.
  4. Ding W, Shen Y, Yang J, He X, Zhang M. Diagnosis of pneumothorax by radiography and ultrasonography: a meta-analysis. Chest. 2011;140(4):859-66.
  5. Jones BP, Tay ET, Elikashvili I, et al. Feasibility and Safety of Substituting Lung Ultrasound for Chest X-ray When Diagnosing Pneumonia in Children: A Randomized Controlled Trial. Chest. 2016;
  6. Laursen et al. Point-of-care ultrasonography in patients admitted with respiratory symptoms: a single-blind, randomised controlled trial The Lancet Respiratory Medicine – 1 August 2014 ( Vol. 2, Issue 8, Pages 638-646)

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The Case of the Pragmatic Wound

cutaneous abscesses

The clinical milieu of the Emergency Department is far from straightforward. The cognitive grime in which we function is rarely conducive to the pristine distinctions drawn by Evidence-Based Medicine (EBM). As such we are often asked to make dichotomous decisions based off a single study, using answers to questions we never intended on asking.

Until recently the management of simple cutaneous abscesses was as straightforward a complaint as there was in Emergency Medicine. Incision and drainage was all that was required. Packing, irrigation and antibiotics had all but been discredited by those in the evidence based know. At least that was until someone went and studied it. A recent trial by Talan et al published in the NEJM examined the utility of enteral antibiotic therapy when added to incision and drainage (I&D) for the management of simple cutaneous abscesses (1). The authors randomized 1265 patients presenting to the Emergency Department with cutaneous abscesses to either I&D and placebo or I&D with the addition of a 7-day course of trimethoprim-sulfamethoxazole. The authors found that patients randomized to the 7-day course of antibiotics had a clinical cure rate of 80.5% vs. only 73.6% in the patients who received I&D alone. The use of trimethoprim-sulfamethoxazole was also found to be superior in a number of secondary endpoints, resulting in lower rates of subsequent surgical drainage procedures (3.4% vs. 8.6%), skin infections at new sites (3.1% vs. 10.3%), and infections in household members (1.7% vs. 4.1%) 7 to 14 days after the treatment period. These improvements in cure rates came at the price of a small increase in gastrointestinal distress, with a 6.5% absolute increase in the rate of GI complaints in patients randomized to receive trimethoprim-sulfamethoxazole.

This was a methodologically rigorous trial, with statistically significant results. Likely its findings will lead to a global shift in practice towards prescribing antibiotics for all simple cutaneous abscesses. And yet despite the strength of these findings, is such a change in practice justifiable?

 Talan et al conducted a pragmatic trial, in which they enrolled all patients older than 12 years old presenting to the Emergency Department with surgically confirmed abscesses larger than 2 cm in diameter conducive to outpatient treatment. The authors limited their exclusion criteria to indwelling devices, suspected osteomyelitis or septic arthritis, diabetic foot ulcers, ischemic ulcers, mammalian bites, wound containing organic foreign bodies, infection of another organ system, perirectal, perineal or paronychial location, intravenous drug use within previous month with fever, underlying skin condition, residence in a long-term care facility, incarceration, or known immunodeficiency. This practical design ensured a heterogeneous cohort of abscesses. A large portion of which had significant concomitant cellulitis. The median area of surrounding cellulitis was 20 cm2 , with approximately 20% of the cohort presenting with a surrounding cellulitic area of greater than 75 cm2 . 11% of the patients had diabetes and 18% had a fever in the days leading up to their presentation to the Emergency Department. Essentially this was not a cohort made up entirely of simple cutaneous abscess. It contained a large quantity of infections that would likely benefit from antibiotics. Despite this, the majority of patients experienced resolution of their abscess with I&D alone. Of the patients who were deemed a clinical failure, very few required further medical therapy, their abscesses ultimately resolved with no further treatment. There was only a 5.6% increase in the number of patients who required addition surgical drainage and a 7% increase in the number of patients started on addition al antibiotics at the follow-up visit between 7-21 days.

The pragmatic design of this study makes for an easy translation to our general Emergency Department population. Unfortunately this very same pragmatism limits a finer, more granular interpretation of the data. In a population that includes abscesses of various shapes and sizes, with varying degrees of surrounding cellulitis, a seven-day course of trimethoprim-sulfamethoxazole provides a moderate degree of clinical value above I&D alone. But it can also be said that the vast majority of patients presenting with cutaneous abscesses will fare equally as well with simple surgical drainage. The question remains, are the patients that failed I&D alone clinically predictable? Meaning were these the patients who had significant surrounding cellulitis, systemic symptoms (fever, malaise) or baseline immune-compromised conditions (diabetes, etc.)? Furthermore this trial fails to address the more subtle unattended consequences of empirically treating all simple cutaneous abscesses with trimethoprim-sulfamethoxazole. This trial was severely underpowered to assess the rate of rare reactions such as Steven Johnson’s syndrome (SJS) associated with the use of trimethoprim-sulfamethoxazole (2). Nor can it evaluate the effects such a change in practice will have on current antibiotic resistance.

Talan et al clearly demonstrate that the majority of patients with simple cutaneous abscesses will improve with I&D alone. The ones that do fail are likely clinically predictable upon presentation. Most will resolve with no further management, with a small minority requiring further surgical drainage or the addition of antibiotics. For the well appearing patient presenting with a simple cutaneous abscesses with minimal cellulitis, a trial of I&D alone seems reasonable.

Clinical medicine is far more complex than the yes/no dichotomy mandated by frequentist methodology. And while the Talan et al trial has provided us with clear evidence that some abscesses will benefit from antibiotics, it does not demonstrate that all abscess do so.

Sources Cited:

  1. Talan DA et al. Trimethoprim-Sulfamethoxazole versus Placebo for Uncomplicated Skin Abscess. NEJM 2016; 374 (9): 823 – 3
  2. Chan HL, Stern RS, Arndt KA, et al. The incidence of erythema multiforme, Stevens-Johnson syndrome, and toxic epidermal necrolysis: a population-based study with particular reference to reactions caused by drugs among outpatients. Arch Dermatol 1990; 126: 43-7.

 

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